Hamming - You and Your Research

What is this talk about?

Richard Hamming — known for Hamming codes, the Hamming window, and decades at Bell Labs — spent his career asking: why do some scientists do great work while others, equally talented, don’t? This talk is his answer.

It is not about managing research. It is about you, individually, deciding to pursue first-class work.

Core Ideas

1. Luck is not the whole story

Hamming acknowledges luck, but points to Pasteur: “Luck favors the prepared mind.” Great scientists produce repeatedly across different problems — too many times to be pure luck. Newton’s own view: if others thought as hard as he did, they would get similar results.

2. Courage is essential

Shannon’s proof that good error-correcting codes must exist — by reasoning about average random codes — required enormous intellectual courage. Hamming sees this as characteristic of great scientists: they think forward under uncertainty and don’t retreat.

3. Work on important problems

This is perhaps the talk’s sharpest point. Hamming would ask colleagues at the chemistry table: “What are the important problems in your field? And are you working on them?” Most weren’t — and most never produced distinguished work.

Crucially, “important” doesn’t mean famous or impossible. It means: you have a reasonable line of attack. Problems without any handle aren’t important, they’re just big.

4. Drive compounds like interest

Bode’s remark: someone who works 10% harder than you will, over a lifetime, vastly outproduce you — because knowledge and skill compound. Each thing you learn makes the next thing easier to learn.

5. Emotional commitment feeds the subconscious

Creativity surfaces from the subconscious. If you are deeply committed to a problem, your subconscious works on it continuously — while you sleep, eat, walk. If you aren’t committed, it wanders. Deep focus is not just discipline; it’s how insights actually arrive.

6. Tolerate ambiguity

Great scientists believe their theory enough to keep going, but doubt it enough to notice cracks. Darwin deliberately wrote down all evidence against his beliefs, knowing his mind would otherwise discard it. Flaws are often the seeds of the next breakthrough.

7. “Great Thoughts” time

Hamming reserved Friday lunches for big-picture thinking only: What will computers do to science? Where is my field going? He kept a mental list of 10–20 important open problems so that when a new result appeared, he could immediately ask: does this bear on one of them?

8. Open vs. closed doors

Working with your door open invites interruptions — but also clues about what matters in the world. Closed-door workers are often more productive day-to-day but drift toward slightly the wrong problems over years.

9. Reframe problems, not just solve them

By reformulating a problem slightly, you can turn a dead-end into progress, a limitation into an asset, and isolated results into generalizable methods. Hamming’s rule: never solve just one instance — solve the class.

10. You must sell your work

Scientists dislike this, but if no one reads your paper, your contribution is zero. Learn to write clearly, give broad and accessible talks (not just technical ones), and speak up in real time — not in a memo three weeks later. Presentation is not decoration; it is half the job.

11. Personality traps that derail good scientists

• Wanting total control — refusing to use the system around you
• Ego assertion — fighting small battles (dress, bureaucracy) that drain energy without payoff
• Anger — it misdirects effort; amusement is more effective than outrage
• Alibis — self-deception about why you haven’t done the important thing yet

12. Shift fields periodically

Early fame can be a trap. After recognition, scientists often try to only do “great” things and stop planting small acorns. Hamming’s prescription: shift your research focus every ~7 years. Entering a new area forces you to think like a beginner again, which is where originality lives.

Memorable Quotes

“If you do not work on an important problem, it’s unlikely you’ll do important work.”

“It is not the consequence that makes a problem important, it is that you have a reasonable attack.”

“The value is in the struggle more than it is in the result.”

“It ain’t what you do, it’s the way that you do it.”

How This Applies to Your Research (Hongting Tsang — Graph Reasoning / LLM)

You are an MPhil student at HKUST working on graph data mining, specifically reasoning with graphs and LLMs under Prof. Yangqiu Song. Hamming’s talk cuts unusually close:

Are you working on an important problem?

Hamming’s test: not “is it hard?” but “do you have a reasonable line of attack?” Graph-LLM reasoning is a genuinely open area with active attack vectors — you have methods, benchmarks, and a community. That clears his bar. But within that space, ask yourself honestly: which specific sub-problem are you working on, and why does it matter beyond your own curiosity or convenience? Can you articulate it in one crisp sentence?

Build your list of 10–20 open problems

Hamming kept such a list always in mind. For you, this might include: Can LLMs reason faithfully over relational structure without hallucinating graph topology? What is the right interface between symbolic graph representations and neural language models? When do GNNs fail where LLMs succeed, and vice versa? Keep this list. When you read a new paper, ask: does this touch one of them?

Emotional commitment + subconscious

As a first-year MPhil student, you are still building identity as a researcher. Hamming’s point about subconscious work is directly actionable: let your current problem sit in your head continuously, not just during work hours. Walk with it. Eat with it. The moments of insight often come when you’re not at your desk.

The closed-door trap

Early-stage researchers often optimize for reading and executing tasks efficiently — but miss the ambient signals of what the community actually cares about. Attend seminars even outside your exact subfield. Talk to people working on adjacent problems. Keep your door (metaphorically) open.

Reframing as a skill

When you hit a wall — a method that doesn’t generalize, a benchmark where you underperform — Hamming’s instinct was to reframe the problem rather than grind harder at the same angle. Could the limitation be turned into a finding? Could a harder version of the problem be easier to characterize theoretically?

Selling your work

You are early in your career, so papers are the primary currency. Hamming’s advice: invest as much time in presentation as in the research itself. A result buried in a poorly structured paper will not move the field. Write for the reader who is skimming — make them stop.

The courage question

Hamming observes that young researchers today often lack the courage to attempt big problems because the environment is highly competitive and the cost of failure feels high. You don’t need to swing for Nobel Prizes. But you should make sure that at least some of what you are doing is on the edge of what you know, not just execution on the safe and well-trodden.

Action Items (Concrete)

• Write down your current “important problem” in one sentence — Hamming’s formulation: what is the problem, and what is your reasonable line of attack?
• Start a running list of 5–10 open problems in your field that you genuinely find important
• Dedicate one session per week to big-picture thinking: where is graph+LLM reasoning going in 5 years?
• For your next piece of work, ask: am I solving one instance, or can I solve the class?
• When you write your next paper section, ask: would a reader skimming the page stop here?

Related Reading

• Shannon, “A Mathematical Theory of Communication” (1948)
• Feynman, “Surely You’re Joking, Mr. Feynman” — similar themes on curiosity and courage
• Paul Graham, “How to Do Great Work” — a modern extension of Hamming’s ideas